A case-control study is an observational design that starts from the outcome. The researcher recruits people who already have a disease or event (the cases) and comparable people who do not (the controls), then looks back to compare how often each group was exposed to a possible cause. The result is an odds ratio. This guide computes one from Doll and Hill’s 1950 lung cancer counts.
Key Takeaways
- Participants enter by outcome status: cases have the outcome, controls do not, and exposure is measured afterwards in both groups.
- Controls must come from the same source population that produced the cases, and they are picked without regard to their exposure.
- The design gives an odds ratio. It cannot give the risk or incidence of the disease, because the researcher decides how many cases and controls to include.
- What the odds ratio estimates depends on how controls were sampled. With controls drawn from people still free of disease at the end of follow-up, it approximates the risk ratio only if the disease is rare; with controls drawn from those at risk when each case occurs (density sampling), it estimates the rate ratio with no rare-disease condition.
- Doll and Hill’s 1950 counts for men (647 of 649 cases smoked, against 622 of 649 controls) give an odds ratio of 14.0.
What is a case-control study?
A case-control study selects people because of their outcome, not their exposure. Some participants have the outcome of interest (cases) and others do not (controls). The investigator then measures past exposure in both groups and asks whether it was more common among the cases. Nobody assigns the exposure, so the design is observational, and it runs backwards, from effect to possible cause.
StatPearls, a clinical reference on the National Center for Biotechnology Information (NCBI) Bookshelf, says the researcher builds a control group “who are similar to the case individuals but do not have the outcome of interest”, then “looks at historical factors” to see which exposures are more common among the cases. Setia, in a methods series for clinicians, adds that “by design, in a case-control study the outcome has to occur in some of the participants”, which is why the design suits rare diseases: the cases are already in hand.
A cohort study runs the other way, enrolling people by exposure and following them to count new cases, which measures risk directly but is slow for rare outcomes. Our guide to the cohort study sets the two designs side by side with the cross-sectional study, and the decision path in our overview of types of research methodology shows how to tell the three apart.
How are cases and controls chosen?
Cases need a written definition anyone could apply the same way, and ideally they are new (incident) cases rather than people who have had the disease for years. Controls must come from the same population that produced the cases, the “study base”, so that any of them would have been counted as a case had they fallen ill. They are picked without looking at their exposure.
Defining the cases. Setia advises that the investigator “should define the cases as specifically as possible”, listing every criterion when a diagnosis rests on several.
Incident or prevalent cases. Knol and colleagues surveyed 150 published case-control studies and found that 125 (83%) used incident cases. With prevalent cases, the odds ratio reflects the rate of getting the disease only “if the duration of disease does not depend on exposure status”: an exposure that helps people survive longer with a disease will be over-represented among prevalent cases.
The study base. Setia explains that cases and controls should come from the same pool of people. In a melanoma study he describes, the 1,167 cases came from the Minnesota Cancer Surveillance System and the 1,101 controls were drawn at random from the state driver’s licence list, so cases also had to hold a licence or state identity card: every case could then have been picked as a control. And “Controls should be selected without regard to their exposure status” (Penn State STAT 507).
Where controls come from. Setia lists three common sources, each with a known weakness.
| Control source | Advantage | Watch for |
|---|---|---|
| Hospital patients with other conditions | Easy to recruit; records of similar quality | Their condition may itself be linked to the exposure |
| Relatives or friends of cases | Relatives share home environment, social class or genes; friends are easy to recruit | Friends especially share habits such as smoking and drinking, which hides those exposures |
| The general population (registers, licence lists, random dialling) | Most likely to fit the study base | Expensive, slow, often low response rates |
How many controls. When cases are scarce, extra controls add power, up to a point: Setia puts the optimum at four controls per case when data are costly, and Partlett and colleagues note that five controls are “only 4% more efficient than using four”.
Matching and over-matching in case-control studies
Matching means choosing controls who resemble each case on a few factors, usually age and sex, so that the two groups are balanced on them. It improves efficiency, but it does not by itself remove confounding by the matched factors: those factors still have to be adjusted for in the analysis. Matching on a factor too closely tied to the exposure, called over-matching, can hide the very association the study is looking for.
In individual matching, each case gets its own controls; in frequency matching, the control group as a whole copies the cases’ distribution, for example the same share of women (Penn State STAT 507). Doll and Hill matched individually: for each lung cancer patient, “a patient of the same sex, within the same five-year age group, and in the same hospital at or about the same time.”
Pearce, writing in the BMJ, stresses that matching “does not control for confounding by the matching factors”. When the matching factor is linked to the exposure, matching makes controls resemble cases on the exposure too, a bias the analysis then has to remove. His hypothetical example is a study of poverty and death that uses living siblings as controls. Because poverty runs in families, each poor case tends to get a poor control, and the study would “find little association between poverty and mortality.”
Partlett and colleagues use the term over-matching for the choice of matching factors “which are not associated with the outcome of interest”, which can cost statistical efficiency. The practical lesson we draw from both papers: match only on factors that predict the outcome and that you would adjust for anyway, then adjust for them in the analysis.
What does a case-control study measure?
It measures the odds ratio: the odds of exposure among the cases divided by the odds of exposure among the controls. An odds ratio above 1 means the exposure was more common among cases, below 1 means less common, and 1 means no difference. It cannot measure the risk or incidence of the disease, because the investigator fixes how many cases and controls are in the study.
With exposure in the rows and case status in the columns, Penn State labels the four cells this way:
| Cases | Controls | |
|---|---|---|
| Exposed | A | B |
| Not exposed | C | D |
The odds of exposure are A / C among cases and B / D among controls, so:
- Odds ratio = (A / C) / (B / D) = (A × D) / (B × C)
Why not a risk? Setia’s example: recruit 50 psoriasis cases and 50 controls, and psoriasis appears in 50% of your sample; add 50 more controls, and it is 33%. Neither is the real prevalence, because “the ratio of cases to controls is not necessarily representative of the ratio in the population” (Penn State).
When does the odds ratio approximate the relative risk?
It depends on how the controls were sampled. If controls are drawn from people still free of the disease at the end of follow-up, the odds ratio estimates the risk ratio (the relative risk) only when the disease is rare. If each control is drawn from the people at risk at the moment a case occurs (density sampling) and the analysis accounts for that matching on time, the odds ratio estimates the rate ratio with no rare-disease condition at all.
Knol and colleagues set out the schemes. With incident cases and controls sampled at the end of follow-up from a fixed cohort, “the odds ratio estimates the risk ratio when the assumption of a rare disease is met.” With controls sampled concurrently with the cases and matched on time, it reflects the rate ratio, provided the analysis takes the time matching into account. With controls sampled at one point from a population that people enter and leave, such as a city, the population must have a stable exposure distribution for the odds ratio to estimate a rate ratio.
Why rarity matters in the first scheme, with made-up numbers: if the exposed have a 2% risk and the unexposed 1%, the relative risk is 2.0, and the odds ratio is (0.02 / 0.98) / (0.01 / 0.99) = 2.02, nearly the same. Now suppose the risks are 40% and 20%: the relative risk is still 2.0, but the odds ratio is (0.40 / 0.60) / (0.20 / 0.80) = 2.67. When the outcome is common, the odds ratio overstates the relative risk.
Knol and colleagues observe that “much emphasis is often placed” on the rare-disease rule, and their own data suggest the emphasis is misplaced. In their survey of 125 studies with incident cases, only 16 needed the rare-disease assumption to read their odds ratio as a risk ratio, while 57 needed a stable population, an assumption that “No investigators mentioned”. The authors conclude that “a stable exposure distribution is much more frequently needed to interpret odds ratios than the rare disease assumption.” In your write-up, say how controls were sampled and what your odds ratio therefore estimates.
Case-control study example: Doll and Hill’s 1950 odds ratio
Doll and Hill interviewed 649 men with lung cancer and 649 men without cancer, matched for age, at 20 London hospitals. Only 2 of the cases had never smoked, against 27 of the controls. In the 2 × 2 table that gives an odds ratio of (647 × 27) / (622 × 2) = 14.0: the odds of having smoked were 14 times higher among the men with lung cancer.
What they did. Between April 1948 and October 1949, four almoners (hospital social workers) interviewed patients notified by the hospitals, using a set questionnaire, and found a matched control without cancer for each lung cancer patient. Patients aged 75 or over were left out. A smoker was “a person who had smoked as much as one cigarette a day for as long as one year”. The series held 709 lung cancer patients, 649 men and 60 women.
The counts. From the paper’s Table IV, in the layout above:
| Men | Lung cancer cases | Controls (no cancer) |
|---|---|---|
| Smokers (exposed) | A = 647 | B = 622 |
| Non-smokers | C = 2 | D = 27 |
| Total | 649 | 649 |
The arithmetic.
- Odds of smoking among cases = 647 / 2 = 323.5.
- Odds of smoking among controls = 622 / 27 = 23.04.
- Odds ratio = 323.5 / 23.04 = 14.0, or by cross-multiplication (647 × 27) / (622 × 2) = 17,469 / 1,244 = 14.04.
Doll and Hill did not print an odds ratio; they compared the proportions of non-smokers (0.3% against 4.2%, P = 0.00000064). The odds ratio is our calculation. For women, 41 of 60 cases and 28 of 60 controls had smoked, which gives (41 × 32) / (28 × 19) = 1,312 / 532 = 2.47.
How precise is 14? Not very. The usual (Woolf) approximation gives a 95% confidence interval (CI) of about 3.3 to 59, almost all of the width coming from the cell with 2 non-smoking cases. The direction is clear; the exact size is not.
A trap in the same table. Saying that 647 of the 1,269 smokers in the table (51%) had lung cancer describes the sample, not smokers: the figure is near 50% only because there was one control per case.
The dose pattern. Among the smokers, 26.0% of the men with lung cancer (168 of 647) reported a most recent habit of 25 or more cigarettes a day, against 13.5% of the male controls who smoked (84 of 622). A dose pattern is harder to explain away than a yes-or-no comparison.
What is a famous case-control study?
One of the most famous is Doll and Hill’s 1950 study of smoking and lung cancer in London, published in the British Medical Journal, together with Wynder and Graham’s American study of the same year in JAMA. Both found that people with lung cancer were far more likely to have smoked, and both became cornerstones of the evidence that smoking causes lung cancer, building on earlier, smaller studies such as Müller’s 1939 study in Germany.
Doll and Hill’s introduction reports Wynder and Graham’s result: of 605 men with certain types of bronchial carcinoma, only 1.3% were non-smokers. Doll and Hill also met the usual objection, that the association runs the other way or comes from a third factor. “The habit of smoking was, however, invariably formed before the onset of the disease”, they wrote, so the disease could not have caused the habit, and they could not “envisage any common cause likely to lead both to the development of the habit and to the development of the disease 20 to 50 years later.” Their conclusion: “smoking is a factor, and an important factor, in the production of carcinoma of the lung.” Their later cohort study of British doctors confirmed the link prospectively.
Bias in case-control studies
Three problems dominate. Recall bias arises when cases remember or report past exposure differently from controls. Selection bias arises when controls do not represent the population that produced the cases. Confounding arises when a third factor is linked to both exposure and outcome. Each can create a false association or hide a real one.
Recall and interviewer bias. StatPearls defines recall bias as “the increased likelihood that those with the outcome will recall and report exposures compared to those without the outcome.” Doll and Hill also worried about their interviewers, who knew the cancer site for all but 61 of the 1,732 cancer patients they saw.
They found a natural test: 209 patients interviewed as lung cancer cases turned out not to have it. If the diagnosis had inflated the smoking histories, these patients should look like the true cases. The counts below come from the paper’s Tables XII and XIII (men and women together); the percentages are ours.
| Group | Patients | Non-smokers | 25 or more cigarettes a day |
|---|---|---|---|
| Lung cancer confirmed | 709 | 21 (3.0%) | 174 (24.5%) |
| Thought to have lung cancer, diagnosis later disproved | 209 | 35 (16.7%) | 16 (7.7%) |
| All other patients without lung cancer | 1,553 | 342 (22.0%) | 150 (9.7%) |
The misdiagnosed patients smoked like the other non-lung-cancer patients, not like the cases. Doll and Hill also compared their chosen controls with all other notified patients and found “no evidence of any special bias in favour of light smokers”.
Selection of controls. Setia’s example of a bad control group: in a hospital study of metabolic syndrome and psoriasis, dermatology patients with tinea pedis (athlete’s foot) make poor controls, because diabetes and obesity predispose to tinea pedis and would inflate the exposure among controls.
Confounding. A confounding variable is linked to both the exposure and the outcome, so it can produce or mask an association. Matching and adjustment handle measured confounders, never unmeasured ones. StatPearls, pointing to the design’s typically retrospective nature, says it can show a correlation but “cannot establish causation”, a distinction our guide to correlation vs causation works through.
What is a nested case-control study?
A nested case-control study is a case-control study run inside an existing cohort or trial. Each time a cohort member develops the outcome, controls are sampled at random from the members still at risk at that moment. Because the cohort recorded exposure before each case’s outcome occurred, the nested design keeps the efficiency of a case-control study while avoiding recall bias and keeping the time order clear.
Partlett and colleagues explain that it was “typically used when it was expensive or difficult to obtain data on a particular exposure for all members of the cohort”: the exposure is measured only in the cases and a few controls each. Controls “may develop the outcome later and become a case themselves, and they may also act as a control for other cases.”
They list three advantages over a standard case-control study: “(1) cases and controls are sampled from the same population, (2) exposures are measured prior to the outcome occurring, and (3) cases can be matched to controls at the time (e.g. age) of the outcome event.”
Their application used 398 growth-restricted preterm infants from a feeding trial, 35 of whom developed severe necrotising enterocolitis, a serious bowel disease. Each case was matched with four infants still at risk on the day of diagnosis, and daily feeding logs showed what each had been fed before that day. Of the 140 matched controls, 8 later became cases themselves.
This is density sampling, so the odds ratio estimates the rate ratio when the analysis accounts for the matching on time (Knol and colleagues).
Strengths and weaknesses of case-control studies
The design is fast, cheap and the natural choice for rare diseases, diseases with long latent periods and outbreak investigations, and one study can test many exposures. Its weaknesses follow from looking backwards: exposure data depend on memory or old records, the controls may not represent the study base, rare exposures are hard to study, and the design cannot give incidence or follow several outcomes.
Strengths. StatPearls notes that for a disease of 1 in 1,000 people a year, a cohort of 1,000 would see about 10 cases in ten years; for rarer diseases, following enough people becomes impractical. Penn State calls the design “powerful enough to identify the cause of the outbreak especially when the sample size is small”, and Setia notes that such studies “can usually be conducted relatively faster and are inexpensive”.
Weaknesses. Cases are chosen for one outcome, so others cannot be studied. A rare exposure leaves little to compare, and Setia suggests a cohort may be the better choice for it. The time order of exposure and outcome “may not be clearly established”, and recall bias, poor controls and confounding remain the standing risks.
How to write up a case-control study
Readers need to see how cases were found, how controls were chosen and matched, how exposure was measured in each group, the counts behind every odds ratio, and which confounders you adjusted for. Health journals expect the STROBE (Strengthening the Reporting of Observational Studies in Epidemiology) checklist for case-control studies: 22 items, several of which ask for information separately for cases and controls.
Item 6(a) asks for “the sources and methods of case ascertainment and control selection” and the rationale for both; 6(b) asks, for matched studies, for “matching criteria and the number of controls per case”; 12(d) asks how matching was addressed in the analysis. Items 8, 13, 14 and 15 carry the footnote “Give information separately for cases and controls.” Item 19 asks for “both direction and magnitude of any potential bias.” Our guide to the methodology section shows where the methods items go.
For the Doll and Hill men, a results sentence reads: “Of 649 men with lung cancer, 647 (99.7%) had smoked, compared with 622 of 649 age-matched hospital controls (95.8%) (crude odds ratio 14.0, 95% CI 3.3 to 59).” Give the counts and label each estimate crude or adjusted.
Where Papero fits
Papero does not choose your controls or calculate odds ratios; those stay with you and your statistics software. It helps with the reading and writing around the study.
Find papers searches more than 250 million papers through OpenAlex and saves any result to your source library. Chat answers questions from your library and open document, citing the passages it used, which helps when you compare how several studies chose their controls. The Review Claims check finds sentences that still need a citation, and references format in APA 7 or any of over 10,000 other styles. What each plan includes is on the pricing page. The literature review workflow shows how these fit together, and the glossary entry on experimental design covers the contrasting approach, where the researcher assigns the exposure instead of looking back at it.
Frequently Asked Questions
What does a case-control study measure?
It measures the odds ratio: the odds of exposure among cases divided by the odds among controls, where 1 means no association. It cannot measure the risk or incidence of the disease, because the researcher decides how many cases and controls to recruit.
What is a retrospective study?
A retrospective study looks back at exposures or events that happened before the study began, using people’s recall or existing records. Case-control studies are often called retrospective because exposure is measured after the outcome has occurred. The label can mislead, though: participants in a case-control study are often recruited as new cases arise, and a retrospective cohort study also uses past records while still comparing exposed and unexposed groups.
What is the difference between a case-control study and a cohort study?
A cohort study selects people by exposure before any of them has the outcome and follows them forward to count new cases, so it measures risk and relative risk directly. A case-control study selects people by outcome and looks back at exposure, so it gives an odds ratio. Case-control studies are quicker and suit rare diseases; cohorts show more clearly that the exposure came first and can follow several outcomes.
What is a nested case-control study?
It is a case-control study run inside an existing cohort or trial. Whenever a member develops the outcome, controls are drawn at random from the members still at risk at that time, and exposure is taken from data or samples collected before the outcome occurred. This cuts cost, because exposure is measured only in cases and a few controls, and it avoids the recall bias of asking people about the past.
Can a case-control study prove causation?
Not on its own. Recall bias, poorly chosen controls and unmeasured confounders can all make an exposure look more common among cases. A causal reading gets stronger when the association is large, rises with the dose, survives checks for bias and is repeated by other designs, as when cohort studies confirmed the smoking and lung cancer link reported by the 1950 case-control studies of Doll and Hill in London and Wynder and Graham in the United States.
Sources
- Doll, R., & Hill, A. B. (1950). Smoking and carcinoma of the lung: Preliminary report. British Medical Journal, 2(4682), 739–748. https://doi.org/10.1136/bmj.2.4682.739
- Tenny, S., Kerndt, C. C., & Hoffman, M. R. (2023). Case control studies. In StatPearls. StatPearls Publishing. https://www.ncbi.nlm.nih.gov/books/NBK448143/
- Setia, M. S. (2016). Methodology series module 2: Case-control studies. Indian Journal of Dermatology, 61(2), 146–151. https://doi.org/10.4103/0019-5154.177773
- Knol, M. J., Vandenbroucke, J. P., Scott, P., & Egger, M. (2008). What do case-control studies estimate? Survey of methods and assumptions in published case-control research. American Journal of Epidemiology, 168(9), 1073–1081. https://doi.org/10.1093/aje/kwn217
- Pearce, N. (2016). Analysis of matched case-control studies. BMJ, 352, Article i969. https://doi.org/10.1136/bmj.i969
- Partlett, C., Hall, N. J., Leaf, A., Juszczak, E., & Linsell, L. (2020). Application of the matched nested case-control design to the secondary analysis of trial data. BMC Medical Research Methodology, 20, Article 117. https://doi.org/10.1186/s12874-020-01007-w
- STROBE Initiative. (n.d.). STROBE statement: Checklist of items that should be included in reports of case-control studies (strobe-statement.org, November 2026). https://www.strobe-statement.org/checklists/
- Penn State Eberly College of Science. (n.d.). Lesson 5: Case control studies. In STAT 507: Epidemiological research methods (online.stat.psu.edu, November 2026). https://online.stat.psu.edu/stat507/Lesson05